ABSTRACT

BackgroundSevere nonmalignant pain affects a large proportion of adults. Optimal treatment is not clear, and opioids are an important option for analgesia. However, there is relatively little information about the comparative safety of opioids. Therefore, we sought to compare the safety of opioids commonly used for nonmalignant pain.

MethodsWe devised a propensity-matched cohort analysis that used health care utilization data collected from January 1, 1996, through December 31, 2005. Study participants were Medicare beneficiaries from 2 US states who were new initiators of opioid therapy for nonmalignant pain, including codeine phosphate, hydrocodone bitartrate, oxycodone hydrochloride, propoxyphene hydrochloride, and tramadol hydrochloride; none had a cancer diagnosis, and none were using hospice or nursing home care. Our main outcome measures were incidence rates and rate ratios (RRs) with 95% confidence intervals (CIs) for cardiovascular events, fractures, gastrointestinal events, and several composite end points.

ResultsWe matched 6275 subjects in each of the 5 opioid groups. The groups were well matched on baseline characteristics. The risk of cardiovascular events was similar across opioid groups 30 days after the start of opioid therapy, but it was elevated for codeine (RR, 1.62; 95% CI, 1.27-2.06) after 180 days. Compared with hydrocodone, after 30 days of opioid exposure the risk of fracture was significantly reduced for tramadol (RR, 0.21; 95% CI, 0.16-0.28) and propoxyphene (0.54; 0.44-0.66) users. The risk of gastrointestinal safety events did not differ across opioid groups. All-cause mortality was elevated after 30 days for oxycodone (RR, 2.43; 95% CI, 1.47-4.00) and codeine (2.05; 1.22-3.45) users compared with hydrocodone users.

ConclusionsThe rates of safety events among older adults using opioids for nonmalignant pain vary significantly by agent. Causal inference requires experimental designs, but these results should prompt caution and further study.

Figures in this Article

Over the past decade, clinicians have received mixed messages about opioids. On the one hand, the World Health Organization suggested that too little attention was being paid to pain, with excessively restrictive opioid prescribing for nonmalignant pain1; on the other hand, the US Food and Drug Administration issued warnings about the dangers of opioids and required manufacturers to document safety through new Risk Evaluation and Mitigation Strategies.2 Despite this confusion, there has been a 50% to 100% increase in the use of opioids in recent years.3,4

Although much attention has been paid to the comparative safety of various selective and nonselective nonsteroidal anti-inflammatory drugs (NSAIDs), relatively little attention has been paid to the comparative safety of opioids. The metabolism and pharmacological properties vary between opioids,5 and previous studies note differences in opioids' relative sedating and constipating effects.6- 9 However, almost no information exists about the comparative safety of opioids regarding serious adverse events, such as fractures, cardiovascular events, hospitalizations for gastrointestinal toxic effects, or mortality. This vacuum of information presents a major problem for patients and providers, who have been warned about the toxicity of NSAIDs. Moreover, expert groups' recommendations include opioid therapy for nonmalignant pain among patients with risk factors for NSAID toxic effects.10,11

Because almost all trials of analgesics are short-term with relatively few patients, the comparative safety of opioid therapy is unlikely to ever be subjected to a randomized controlled trial. With this in mind, we designed an observational study comparing the safety of opioid therapy for nonmalignant pain in older adults. The safety events that were examined included several specific events, such as fracture, cardiovascular events, and gastrointestinal bleeding or bowel obstruction. As well, we examined several composite safety events, including toxic effects leading to hospitalization or death and all-cause mortality.

METHODS

STUDY COHORT

The cohort consisted of Medicare beneficiaries from 2 US states who qualified for pharmaceutical assistance programs for low-income older adults between January 1, 1996, and December 31, 2005. These state-run programs provide medication insurance coverage for all drugs without restriction. From the eligible pool of subjects, we selected adults who had filled at least 1 prescription for an opioid. To restrict use to nonmalignant indications, persons with a diagnosis of cancer in the 365 days before the prescription date were excluded. We required subjects to demonstrate consistent health care system use in the preceding 365 days, as noted by a health care or pharmacy claim in each of the four 3-month periods before the start of an opioid. To maximize comparability of study subjects, we further excluded individuals who had filled a prescription in the preceding 365 days for an NSAID (selective or nonselective) or an opioid. Finally, subjects with any evidence of hospice or nursing home care in the preceding 365 days were excluded (Figure 1).

PROPENSITY SCORE MATCHING

We matched subjects prescribed the 5 most common opioids used for nonmalignant pain—hydrocodone bitartrate, codeine phosphate, oxycodone hydrochloride, propoxyphene hydrochloride, and tramadol hydrochloride—using a propensity score constructed from the subjects' baseline covariates.12 A propensity score estimates the probability of receiving 1 treatment exposure vs a reference exposure; matching on a propensity score balances the treated and reference subjects with respect to the score's components. Four separate propensity scores were estimated using multivariate logistic regression models. Each opioid group was compared with the referent exposure, hydrocodone. Matching was accomplished using a “greedy” matching routine13 by finding a subject starting therapy with a different opioid who had a propensity score identical to the fifth decimal place; if no match was found, we then searched the fourth, third, second, and first decimal places. If no match was found, the exposed subject was dropped from the analysis. Because the four 2-way propensity score models shared a common reference group, we created exposure cohorts comparable across baseline covariates by restricting to matched pairs in which the subject in the hydrocodone group was successfully matched to all the other 4 opioid arms.

The propensity scores were based on variables that can be measured in claims data (demographics, diagnoses, surgical procedures, and pharmacy dispensings) and may predict any of the clinically significant safety events we studied (Table 1 provides a list of covariates included in the propensity score, and eTable 1 gives their diagnosis codes). Variables were determined from data for the 365 days before the start of analgesic exposure—the index date. The calendar year of the index date was also included in the propensity score.

A study protocol was developed before the analyses were performed. The study was approved by the Partners Healthcare Institutional Review Board.

SAFETY EVENTS

Several adverse events were of particular interest to us, including fracture, cardiovascular events, and gastrointestinal bleeding or bowel obstruction. We also attempted to capture the composite safety of these drugs by assessing the data for any adverse event leading to hospitalization, any adverse event leading to death, and all-cause mortality. For the composite safety events, other common drug-associated adverse events were also included, such as kidney insufficiency,14 hepatotoxic effects, or falls. Thus, subjects were considered to have experienced a composite safety event if they had an individual safety event leading to hospitalization or death or if they died.

Each of these outcomes was defined on the basis of health care utilization data, using diagnosis and procedure codes (eTable 1 provides a list of all codes used and supporting studies). Our definition of fractures included hip, pelvis, wrist, and humerus fractures15 but not spine fractures because new vertebral compression fractures cannot be reliably identified in claims data.16 Cardiovascular events included myocardial infarction, stroke, heart failure, revascularization, and out-of-hospital cardiac death.17- 20 Out-of-hospital cardiac death was based on an algorithm we developed that uses health care utilization data in which a death is noted in a subject with known cardiovascular disease but no previous cancer or human immunodeficiency virus infection. Gastrointestinal outcomes included upper and lower gastrointestinal tract bleeding and bowel obstruction.21

OPIOID EXPOSURE

Data on the opioid exposures, as well as other medications, came from pharmacy dispensing data. The pharmacy data include drug name, daily dosage, and days of supply. The primary analyses considered subjects as being opioid-exposed from the day after the first dispensing through 7 days after the last available dose. This definition of exposure is often described as “treated.” If a second type of opioid was received, that subject was censored at the date the second opioid was dispensed. In secondary analyses, this period after the last available dose was varied from 7 to 3 days. Other censoring events included end of eligibility, death, switching to another opioid, or the event of interest. Subjects were not censored at the first of any event to allow for competing risks to be fully captured in a given end point analysis.

STATISTICAL ANALYSES

We compared the baseline characteristics of the propensity score–matched cohorts. Incidence rates with 95% confidence intervals (CIs) were calculated for all safety events for each of the 5 opioid cohorts. The primary analysis estimated the relative risk for each serious safety event, as well as the composite safety measures, by calculating the incidence rate ratio (RR), ending follow-up after 30 and 180 days of opioid exposure.

Secondary analyses were performed to examine whether the primary findings were robust. First, a dosage analysis was performed that categorized the starting dosage of each opioid as low, medium, high, or very high (eTable 2 provides dosage categories). Second, analyses were performed that allowed for as much follow-up time as was available (vs ending follow-up 30 or 180 days after initiation of opioid therapy). Third, we conducted analyses that considered subjects as treated even after no further drug was available, truncating at 30 or 180 days after initiation of therapy. This conservative type of analysis mirrors an intention-to-treat analysis in which the influence of biases occurring after the initiation of drug therapy is limited. Fourth, we varied the allowable gap after an opioid prescription ends until censoring from 7 days (primary analysis) to 3 days. Fifth, we began follow-up with the second opioid prescription. All the aforementioned secondary analyses calculated incidence rate ratios as an estimate of the RR. Finally, because many opioid preparations include acetaminophen, this was added as a covariate when it was part of the initial prescription, and relative risks were calculated in Cox proportional hazards regression models.

RESULTS

The study cohort was assembled from a very large pool of Medicare beneficiaries who also had drug benefits and had evidence of opioid use during the study period, 1995 to 2005 (n = 541 867). After applying the inclusion and exclusion criteria, 143 482 (26.5%) potentially eligible subjects were available for matching (Figure 1). We were able to match 6275 subjects in each of the 5 opioid groups, resulting in inclusion of 5.8% of the potentially eligible subjects.

After matching, the baseline characteristics for the matched cohorts were well balanced across opioid exposures (Table 1). The groups had a mean age of 79 years; 80.9% were women and 91.0% were white. The mean number of comorbid conditions was 1.7. The mean number of acute care hospital days was slightly higher for oxycodone users than for users of the other opioids, and fewer oxycodone users were women.

Although the median supply of opioids was for between 2 and 6 weeks, some subjects received opioids for many months (eTable 3). The incidence rates for all 6 of the safety events were high after 30 days of opioid use (Table 2). Hydrocodone was used as the reference exposure, and RRs were calculated across all 6 safety events after 30 and 180 days of opioid exposure (Table 2 and Table 3). The risk of cardiovascular events was similar across opioid groups in the 30-day analysis. However, by 180 days, it was elevated for codeine (RR, 1.62; 95% CI, 1.27-2.06). During the first 30 days of opioid treatment, the risk of fracture was significantly reduced for tramadol users (RR, 0.21; 95% CI, 0.16-0.28) and propoxyphene users (0.54; 0.44-0.66). The risk of gastrointestinal safety events did not differ across opioid groups at either time point. All-cause mortality was elevated after only 30 days for oxycodone users (RR, 2.43; 95% CI, 1.47-4.00) and codeine users (2.05; 1.22-3.45).

In secondary analyses, we found results consistent with the main findings (Figure 2). There was no clear gradient of risk across dosages except for the fracture end point, for which the high-dosage relative risks regressed toward the null. An alternative dosage analysis categorized dosages according to equi-analgesic levels and found similar results (data not shown). Further secondary analyses tested whether the results were sensitive to different assumptions regarding the exposure period. eFigure 1 displays results for the 6 safety events across different assumptions and finds small differences in relative risk. One notable exception is that, when follow-up began with the second prescription, the results for fractures all regressed to the null (eFigure 1). Varying the period after the last available opioid dose before censoring from 7 to 3 days made no important difference in our results (eTable 4). A further secondary analysis included acetaminophen as an indicator term in Cox proportional hazards regression models and found no substantial change in the relative risks from the original analyses while observing subjects for as long as their opioid treatment continued (eTable 5).

COMMENT

Many older adults received prescriptions for opioid analgesics for nonmalignant pain, but little is known about their relative safety. We compared the safety of opioid analgesics for nonmalignant pain among older adults, using data from large health care–utilization databases. We found that the relative risks varied by opioid and by adverse event and even varied by treatment duration. Notable relative risks included an elevated risk of cardiovascular events for codeine users after 180 days, a reduced risk of fracture for tramadol and propoxyphene users after 30 and 180 days, and an increased risk in all-cause mortality after only 30 days for oxycodone and codeine users. This study's findings do not agree with a commonly held belief that all opioids are associated with similar risk.

The results of this study need to be considered in light of the limitations of our methods. First, we analyzed typical practice data from a nonrandomized setting. Thus, these results may be biased by residual confounding, in which factors influence the prescription of a given opioid and the safety events in question. This potential confounding bias limits the causal inference and renders this a study of associations. Although this is a serious limitation of our method, we doubt that the comparative safety of multiple opioids will ever be adequately tested in a randomized controlled trial. We matched subjects in each of the 5 opioid groups using a propensity score that takes into account many of the measured confounders available in the study database. The list of variables included in the propensity score is based on our desire to create a common propensity score across outcomes. As Table 1 demonstrates, after matching, the measured characteristics of subjects were similar across the 5 groups. Differences persisted in some variables, especially those that occurred with low frequency. Second, the study database was limited because it consisted of health care and pharmacy utilization data without information about cause of death from death certificates, pain levels, functional status, aspirin or tobacco use, or over-the-counter medication use. This may have led to some misclassification of exposures and outcomes. Because opioids are dispensed only with a prescription, exposure misclassification should be minimal. As far as outcomes, the vast majority of the disease definitions have been found to be accurately coded in this type of data. Moreover, we anticipate that misclassification of outcomes would be random. Third, we studied a group of older low-income adults; thus, the generalizability of our results need to be proved in other cohorts. Finally, we observed a limited number of events in several outcome-exposure relationships. Thus, our ability to prove the safety of a given opioid for a specific outcome is limited; this is clear from the width of the 95% CIs for some of the relative risks provided in Tables 2 and 3.

Our study exhibits a number of important strengths. The use of the propensity score–matched cohorts provides for well-balanced study cohorts, facilitating the calculation of incidence rates and risk differences. The risk differences can be used to calculate numbers needed to treat, a useful metric for clinicians considering how to apply epidemiologic results to practice. As well, the matched cohort design allows one to examine the comparative effectiveness of multiple exposures across many outcomes. Such a “matrix design” might be considered for further comparative effectiveness studies. In addition, we pursued several types of secondary analyses that yielded small but predictable differences. While the use of multiple analytic strategies may seem to be a weakness, each analysis asks the same question but in slightly different terms. When there is consistency in the findings, the results should be considered more robust.

Several of our findings require discussion. We found an increased risk of cardiovascular events among codeine and propoxyphene users compared with hydrocodone users. We are not aware that differences in cardiovascular risk have been reported among opioids. However, at least 1 study observed an increased risk of cardiovascular death among subjects with unstable angina who received morphine.22 Our group previously observed an increased risk of cardiovascular events in opioid users compared with nonselective NSAID users.23 This finding may be confounded, but Table 1 does not suggest this possibility.

The reduced risk of fracture among tramadol users compared with hydrocodone users is also a novel finding. Previous studies have shown an increased risk of fracture among opioid users compared with nonusers.24- 26 One study compared codeine users with propoxyphene users and found no difference in risk.24 Opioids may cause fractures through at least 2 mechanisms—an increased risk of falls27 and an effect of opioids on bone metabolism through androgens.28 It is possible that either or both mechanisms may underpin the reduced risk of fractures we observed among tramadol users, perhaps the increased risk of falls being important in the 30-day analysis and the effects on bone metabolism influencing the longer-term analyses. Finally, the increased all-cause mortality we observed for codeine and oxycodone users may relate to cardiovascular events or other unmeasured confounders. We did find that relative risk decreased in the high-dosage categories, suggesting that the risk of opioid use may equalize when used at such dosages. This result also requires confirmation in other data sets.

In summary, we explored possible differences in risk between opioids commonly used for nonmalignant pain and found that the risk varied by agent across many of the adverse events examined. The risks were not explained by the dosage being prescribed and did not vary across a range of sensitivity analyses. The risks were substantial and translated into numbers needed to treat that would be considered clinically significant. Our findings regarding cardiovascular risk were surprising and require validation in other data sets.

Author Contributions: Dr Solomon had full access to all the data in the study and takes responsibility for the integrity of the data and the accuracy of the data analysis. Study concept and design: Solomon, Rassen, and Schneeweiss. Acquisition of data: Solomon and Levin. Analysis and interpretation of data: Solomon, Rassen, Glynn, Garneau, Levin, Lee, and Schneeweiss. Drafting of the manuscript: Solomon and Garneau. Critical revision of the manuscript for important intellectual content: Solomon, Rassen, Glynn, Levin, Lee, and Schneeweiss. Statistical analysis: Solomon, Rassen, Glynn, and Schneeweiss. Obtained funding: Solomon. Administrative, technical, and material support: Lee and Schneeweiss. Study supervision: Solomon.

Financial Disclosure: Dr Solomon reports serving as an unpaid member of a celecoxib trial executive committee sponsored by Pfizer and also as an unpaid member of the Data Safety Monitoring Board for an analgesic trial sponsored by Pfizer.

Funding/Support: This study was supported under contract 290-05-00XX-1 27EHC from the Agency for Healthcare Research and Quality, US Department of Health and Human Services, as part of the Developing Evidence to Inform Decisions about Effectiveness (DECIDE) program.

Role of the Sponsors: The authors of this report are responsible for its content. Statements in the report should not be construed as endorsement by the Agency for Healthcare Research and Quality or the US Department of Health and Human Services.

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